acceptodds
Under review as a conference paper at ICLR 2027

C^3: Rethinking Process Supervision via Confidence-Guided Credit Correction in Multi-Turn Reinforcement Learning

Abstract

Large language models are increasingly trained as multi-turn agents that interact with external tools. However, outcome-only reinforcement learning can assign incorrect credit to local bad patterns: when a trajectory succeeds, erroneous behaviors in intermediate turns may still receive positive advantage and be reinforced. To address this issue, we propose Confidence-Guided Credit Correction (C³), a plug-in method for local credit correction. C³ identifies bad-pattern spans and selectively corrects positive credit after advantage estimation, with the correction strength adaptively controlled by the behavior policy's confidence in the corresponding behavior, while leaving the task reward and original credit estimation unchanged. Across multiple multi-turn benchmarks, C³ improves performance under both critic-based and critic-free reinforcement learning methods. Injecting the same behavioral signals as turn-level or outcome rewards does not consistently improve performance. Our results show that local credit correction provides an effective form of process supervision for outcome-driven RL.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Multi-Turn Reinforcement Learning, LLM Agents, Credit Assignment, Process Supervision

Reviews

Among:
Shape:
1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_L5TCOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
2
Soundness
2
Read review
Paper summary

The paper identifies a "misguided reinforcement" problem in multi-turn agentic RL with outcome-only rewards: tokens belonging to bad local behaviors (invalid tool calls, repeated queries) frequently receive positive advantages on successful trajectories. C3 is a lightweight post-hoc correction applied between advantage estimation and the actor update — positive advantages on detector-flagged spans are flipped, scaled by the behavior policy's confidence on that span — leaving the reward, return, and critic untouched. Experiments cover both PPO and GDPO on Search QA (7 benchmarks) and WebShop.

Critical strengths

The phenomenon is documented convincingly. The token-level audit showing that ~29% of detector-flagged tokens still receive positive credit, together with the training-dynamics analysis, is a useful observation for anyone doing multi-turn RL. I also found the process-reward comparison genuinely informative: injecting the same signal as a turn-level reward makes things worse (query loops roughly triple, WebShop collapses late in training), which supports the paper's central point that where a process signal enters matters.

The method itself is simple, cheap, and genuinely plug-and-play, and it shows consistent — if modest — gains across two RL paradigms, two environments, and a third-party recipe (T2PO), which is more coverage than most papers of this type provide.

Critical weaknesses

The baseline coverage is thin for a paper titled "rethinking process supervision." None of the existing turn/step-level credit assignment methods discussed in the related work (Turn-PPO, StepSearch, GiGPO, etc.) are compared against — the only process-supervision baseline is the authors' own turn-level penalty. So we learn that C3 beats naive reward injection, but not whether it beats existing process supervision.

The evidence also has statistical weaknesses: the error bars come from sampling at test time, not from multiple RL training runs, which is where most of the variance lives; the flagship gain (2Wiki +11.5 under PPO) flips sign under GDPO (-2.2) and is never really explained; WebShop numbers use best-checkpoint selection. On the method side, the design is purely heuristic — the token-level confidence variant is worse than doing nothing, there is no ablation with constant correction strength, and the detector's precision/recall is never measured, so the damage from false positives is unknown.

Questions for authors
  1. How does C3 perform with constant correction strength (e.g. κ=1, severity only)? If that already matches, is the confidence weighting buying anything? And why should high-confidence bad behavior be corrected more strongly rather than less?
  2. What are the detector's precision and recall, especially for near-duplicate query loops? How sensitive are the results to the similarity threshold?
  3. Why does 2Wiki improve by +11.5 under PPO but degrade under GDPO? And how many independent RL training runs underlie each number in the main table?
4 comments
AuthorsOpenReview ↗

Response to Reviewer L5TC(1)

We thank the reviewer for recognizing the value of our token-level audit, process-reward comparison, and lightweight integration. In response to the reviewer’s concerns, we have expanded the baseline evaluation with T²PO, added controlled ablations of confidence-guided correction, and conducted further analyses of detector reliability and the 2Wiki performance reversal.

W1 — The baseline coverage is thin: existing turn/step-level credit-assignment methods are not compared.

A: We thank the reviewer for pointing out the limited coverage of agent-specific process-supervision approaches. We have expanded the T²PO evaluation to Search QA and added Avg@4 evaluations for WebShop. T²PO is an agent-RL recipe featuring GiGPO-style credit assignment, and we evaluate it both with and without C³. This additional experiment tests whether C³ provides complementary benefits on top of an existing agent-specific credit assignment mechanism, rather than relying solely on the PPO/GDPO settings in our original evaluation.

The new comparisons are reported in Tables 1–2 of the revised manuscript, with the added setup and results highlighted in blue, particularly in Sections 5.1–5.2:

EvaluationT²POT²PO+C³
Search QA macro strict EM51.05 ± 0.0651.49 ± 0.18
WebShop task score86.52 ± 0.6489.09 ± 0.37
WebShop success76.50 ± 0.77%76.70 ± 0.89%

We appreciate that comparisons with additional agent-RL recipes such as Turn-PPO and StepSearch would provide further insights. In this revision, we have extended our evaluation with T²PO to broaden the coverage of agent-specific credit assignment methods. We also clarify that the process-reward PPO control examines a complementary intervention point: it applies event-level penalties before return and advantage estimation, whereas C³ operates on the resulting token-level advantages (Appendix B.2).

W2.1 & Q3 — The error bars come from sampling at test time. How many independent RL training runs underlie each number in the main table?

A: We thank the reviewer for raising this important point. Each experimental arm currently uses one independent training run. The reported error bars quantify variation across stochastic evaluations of a trained checkpoint, rather than variance across independent training runs. Due to limited computational resources and time during the rebuttal period, we were unfortunately unable to conduct additional independent training runs. We agree that multi-seed experiments would provide stronger evidence of training robustness.

Nevertheless, we have evaluated C³ across multiple agent-RL methods (PPO, GDPO, and T²PO) and different tasks, observing consistent improvements across these settings. These results provide complementary evidence across training methods and tasks. For completeness, Table 1 reports the PPO+C³ result of 50.20 ± 0.10, corresponding to a 2.41-point macro improvement over PPO, and Appendix B.3 details the evaluation samples and standard-deviation calculation.

W2.2 & Q3 — Why does 2Wiki improve by +11.5 under PPO but degrade under GDPO?

A: We thank the reviewer for highlighting this difference between PPO and GDPO. The opposite changes are concentrated in comparison questions, particularly those requiring yes/no answers. We break down 2Wiki performance by question type to identify which subsets drive the PPO gain and the GDPO decline.

2Wiki question typeQuestionsPPO → PPO+C³ EM (%)GDPO → GDPO+C³ EM (%)
Bridge comparison2,75151.06 → 85.6581.64 → 68.73
Comparison3,04075.95 → 92.2481.05 → 74.47
Compositional5,23650.76 → 51.3849.99 → 52.94
Inference1,54946.16 → 44.2238.90 → 47.55

Among the 1,295 yes/no questions, PPO+C³ improves EM from 26.72% to 82.01%, whereas GDPO+C³ reduces it from 48.73% to 20.25%. These changes contribute +5.69 and −2.93 percentage points, respectively, to overall 2Wiki EM. On the remaining questions, GDPO+C³ contributes a positive aggregate gain of +0.81 points.

Trajectory analysis further identifies answer-type selection as a key behavioral difference. Among all evaluated responses to the 1,295 yes/no questions, including responses without an answer, the fraction that contains an answer but not a standalone "yes" or "no" decreases from 63.06% to 6.72% with PPO+C³, but increases from 41.80% to 71.95% with GDPO+C³. For example, on the same nationality-comparison question, PPO changes its answer from "Germany" to "yes" after adding C³, whereas GDPO changes from "Yes" to "German." These observations suggest that the reversal is associated with how C³ affects answer-type selection under different optimization algorithms. A plausible explanation is that PPO and GDPO's different advantage estimation and optimization dynamics lead to different uses of the modified token-level learning signals.

AuthorsOpenReview ↗

Response to Reviewer L5TC(2)

W2.4 & Q1 — The token-level confidence variant is worse than doing nothing. How does C³ perform with constant correction strength, and why correct high-confidence bad behavior more strongly?

A: We thank the reviewer for raising these important questions about the confidence design. To better examine its contribution, we have added constant-strength and masking controls. Figure 7 (left) uses the C³ endpoint from Table 1 and compares it with the following alternatives.

Correction ruleMacro strict EM (%)
Token probability44.73 ± 0.18
Geometric span mean49.06 ± 0.22
Arithmetic span mean, C³50.20 ± 0.10
Whole-bad-turn masking48.74 ± 0.25
Constant κ = 0.546.56 ± 0.44
Constant κ = 1.050.16 ± 0.25

The token-level variant underperforms PPO (44.73% vs. 47.79%). We suspect that token likelihood may misallocate correction according to lexical predictability: within a flagged turn, reusable formatting may receive more weight than tokens defining the offending action, potentially interfering with valid behavior. Span averaging avoids this issue by applying a uniform gain across the behavioral event.

C³ and constant κ=1.0 achieve comparable strict EM (50.20% vs. 50.16%). However, in the separate four-generation behavior evaluation (Figure 7, right), C³ yields fewer query loops (69/206,852 = 0.0334% vs. 147/206,852 = 0.0711%) and behavior-union violations (90/206,852 = 0.0435% vs. 218/206,852 = 0.1054%). This supports the benefit of confidence guidance: confidence reflects the policy's preference for an action, not its correctness. Thus, stronger correction is applied when an undesirable behavior is more strongly reinforced by the current policy.

W2.5 & Q2 — What are the detector's precision and recall, especially for near-duplicate query loops? How sensitive are the results to the similarity threshold?

A: We thank the reviewer for raising this question. We conducted an LLM-assisted audit of 427 query-level items sampled across four policies and similarity strata. A single LLM reviewer first labeled the items blind to detector predictions; the reported estimates use the final adjudicated labels. The detector achieves 95% precision for identifying repeated information needs and 90% precision (95% CrI: 80–94%) for unnecessary repeated searches, with all 33 sampled exact-match triggers correctly identified. Recall is substantially lower because many semantic repetitions use different wording. The audit supports this qualitative gap, but does not provide a reliable population recall estimate.

We further examined the effect of varying the near-loop similarity threshold:

ThresholdFlagged actions (est.)Same-information precisionUnnecessary-repeat precision
≥ 0.95~21296%96%
≥ 0.90 (used)~53295%90%
≥ 0.85~1,21095%87%
≥ 0.80~2,68495%81%

Lower thresholds detect more potential repetitions but also introduce more false positives. The selected threshold prioritizes precision to avoid incorrectly suppressing useful behaviors. This analysis is based on fixed trajectories and does not measure training performance under different thresholds.

Thanks for the clarifications and I will maintain my scoring.

Thank you for taking the time to review our response and consider the additional experiments and clarifications. We sincerely appreciate your thoughtful feedback and constructive suggestions, which have helped us improve the manuscript.

Reviewer_QeQGOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper diagnoses what it calls misguided reinforcement in outcome-driven RL for multi-turn agents: under whitened or group-relative credit, tokens inside locally undesirable behaviours — malformed tool calls and repeated queries — can still carry positive advantage and therefore be reinforced by the policy update. It proposes C^3, a post-estimation operator that sits between advantage estimation and the actor update. A rule-based detector (Appendix B.1, Table 5) localises an event as e = (I_e, d_e, q_e, J_e), taking the whole responsible turn as the correction span I_e, the parsed tool/answer action as the confidence span J_e, and a severity q_e ∈ (0,1] — 1.0 for malformed actions and exact query loops, 0.5 for near loops (trigram Jaccard ≥ 0.9, length ≥ 8). Inside I_e, a token with Â_i > 0 has its advantage replaced by Ã_i = −κ_i q_i Â_i (Eq. 8), where κ_i is the behaviour policy's confidence in the corresponding action, computed as the arithmetic span mean (1/|J_e|) Σ_j π_{θ_k}(z_j | s_j) (Eq. 5) and detached from the graph. Tokens with Â_i ≤ 0, and tokens outside the span, are untouched; the reward, the returns, and the critic targets are left unchanged, so the operator is claimed to be a plug-in applicable to both critic-based and critic-free optimization (Algorithm 1, §4.3). The optional zero-advantage branch −βκ_i q_i has β = 0 in every experiment and is dead code as reported. A motivating audit (§4.1) reports that 18,460 of 63,511 valid tokens inside flagged spans (29.07%) received positive base advantage in one instrumented PPO run.

Critical strengths

C^3 changes one line of the actor objective — a sign flip on a subset of positive advantages — and leaves the reward, the returns, the critic, and the rollout pipeline alone. That is not a rhetorical claim in this paper: the same operator is applied after PPO's GAE-plus-whitening, after GDPO's grouped axis normalisation (Eq. 15), and after the official T2PO actor-side advantages in Appendix C.1, and it improves the reported metric in all three. This matters for the recommendation because it locates the contribution where the field actually has a gap. The paper's own comparison set makes the point: the reward-side alternative it tests (turn-level process PPO) requires injecting a penalty into the return before GAE, where it leaks backward through the discount into preceding tokens — the mechanism Figure 1(b) illustrates — and it degrades. A correction applied after estimation cannot leak by construction. Even if the specific operator is wrong, the architectural claim that where the process signal enters matters more than how strong it is is a real and transferable finding, and the T2PO replication is the cleanest evidence for it in the paper.

Critical weaknesses
  1. By the paper's own numbers, the behaviour C3 targets occurs in roughly a tenth of a percent of trajectories: PPO's query-loop rate is 0.159% and C3's is 0.064% over 51,713 questions (§6.1), i.e. about 82 versus 33 trajectories. Deleting or repairing fifty trajectories cannot produce a +2.41-point macro-EM gain; at the reported rates the correction can account for a few hundredths of a point. The gain therefore has to arrive through some indirect channel — a global shift in the gradient field, a change in exploration, or optimization noise — and the paper never separates these from the stated channel. The four controls that would do so are all absent: no placebo that applies the identical sign flip to randomly chosen spans of matched count and length; no constant-κ arm (κ = 1), so the "confidence-guided" in the title is never tested against the simplest possible control; no masking arm (Ã_i = min(Â_i, 0)) or zero-out arm, so reversing credit is never compared to merely removing it; and no clamp-to-a-fixed-negative-advantage arm, so the proportionality of the penalty to the advantage it is correcting is never tested. Without the last two the paper cannot distinguish its own hypothesis from unlikelihood training on flagged spans — a different method with a different justification. This is consequential because it is precisely the claim the abstract makes, and the entire framing of "credit correction" rather than "penalty injection" depends on it.

  2. The paper cites FACTOR (Ma et al., 2026) as related work but never compares against it, does not discuss VETTA [2610.08402], and does not engage CrEST [2608.13179], which separates the magnitude from the direction of credit — the exact distinction a sign-reversing operator turns on. No published token-level credit-assignment baseline is run, and no simple negative-advantage clipping baseline either. The "first to identify misguided reinforcement" framing is not substantiated: that outcome rewards reinforce bad sub-behaviours is a known observation, and what is new here is the instrumented measurement, not the phenomenon. The four case studies (D.2–D.4, Figures 12–14) state no selection procedure, and their before/after pairs are different policies — and in D.3 versus D.4 even different first candidates — so they cannot show a local credit effect; in D.2 the corrected trajectory diverges in the very first query, which is not a flagged-span effect at all. Finally, the generality claim is narrower than the framing: the detector is two hand-written rules for one environment, the SFT corpora were filtered to exclude exactly those two behaviours (Appendix A.3: retained traces must be "non-repeating, and free of invalid actions"), and the third environment's gain (T2PO, 81.2 → 82.2) is a single run of a single point.

Questions for authors
  1. What is the per-batch correction rate: how many tokens per training batch have Â_i > 0 inside I_e and are actually flipped, as a fraction of all generated tokens, for each arm? Given that the query-loop rate is 0.159% of trajectories (§6.1) while the PPO gain is 2.41 macro-EM, please account for the mechanism by which correcting a few hundredths of a percent of tokens produces the reported effect. If the answer is an indirect gradient effect, say so explicitly and revise the "local credit correction" framing accordingly.

  2. Please report the full checkpoint-selection protocol. Table 1's rule is unstated; Table 2 uses "best-success checkpoint" on the 500-task split that Appendix A.2 and C.3 also use for validation; Table 6 reports different iterations per arm (70 vs 120); Table 3 is a final checkpoint. Is there any split on which checkpoints were selected that is disjoint from the reported one? Please give the final-checkpoint number and the mean over the last N checkpoints for every arm, alongside the selected numbers.

  3. Position C3 against VETTA [2610.08402], FACTOR [2608.07118] (cited but not compared), CrEST [2608.13179], and a plain min(Â, 0) clamp. Which of these already provide local credit correction, and what does the confidence weighting add beyond them? Also, how does C3 degrade if the detector is noisy or learned (e.g. an LLM judge) rather than a hand-written rule?

3 comments
AuthorsOpenReview ↗

Response to Reviewer QeQG (1)

We thank the reviewer for encouraging a clearer distinction between local behavioral correction and general credit assignment, and for asking us to substantiate our methodological claims. In response, we provide additional training-time correction statistics, new ablation results, a clarification of checkpoint selection, and a more precise interpretation of the qualitative trajectory examples.

W1.1 & Q1 — What is the per-batch correction rate, and how does correcting so few tokens produce the reported effect?

A: We thank the reviewer for raising this important question. We would like to clarify that evaluation-time endpoint violation rates and training-time correction coverage measure different quantities. C³ modifies token-level advantages during RL training, rather than directly repairing trajectories at inference time. Therefore, the small number of remaining endpoint violations does not reflect the extent of training signals modified by C³.

To provide a more direct view of its training-time coverage, we report the following statistics from the complete actor training logs:

Training statisticPPO+C³GDPO+C³
Total training trajectories200,448213,248
Trajectories with detected undesirable behaviors907 (0.4525%)560 (0.2626%)
Valid actor-training tokens35,455,87632,813,764
Tokens entering the correction branch18,460 (0.0521%)10,465 (0.0319%)
Update batches with at least one correction338/783 (43.17%)135/833 (16.21%)

Although correction is sparse at the token level, it is distributed across a substantial fraction of training updates. Importantly, C³ modifies the policy's gradient updates through shared model parameters, so its influence is not necessarily restricted to the directly flagged tokens or trajectories.

W1.2 & Q3 — No random-span placebo, constant-κ, masking/zero-out, or fixed-negative-advantage arm.

A: We thank the reviewer for suggesting these controls. We have added constant-strength and whole-bad-turn masking controls to examine the contributions of confidence weighting and sign reversal. The results are summarized below (Section 6.2 and Figure 7).

Rule on a marked spanPositive base advantageNegative base advantageMacro strict EM (%)
Constant κ = 1 reversal−qᵢÂᵢPreserved50.16 ± 0.25
C³−κᵢqᵢÂᵢPreserved50.20 ± 0.10
Whole-bad-turn masking0048.74 ± 0.25

C³ and constant κ=1 achieve comparable task accuracy (50.20% vs. 50.16%), but C³ yields fewer query loops (69 vs. 147) and behavior-union violations (90 vs. 218) in the separate four-generation evaluation. Constant κ=0.5 achieves 46.56 ± 0.44 macro strict EM. These results suggest that confidence weighting improves behavioral suppression at comparable task accuracy, while whole-bad-turn masking performs worse than selective sign reversal.

Importantly, constant κ=1 still scales the correction with the original advantage magnitude, whereas a fixed-negative-advantage control (−cqᵢ) would remove this dependence. Our masking control also zeros both positive and negative advantages, and is therefore different from the positive-only clamp min⁡(A^i,0)\min(\hat A_i,0). Due to the limited time and computational resources available during the rebuttal period, we were unable to conduct the additional fixed-negative-advantage, positive-only clamping, and matched random-span experiments. We acknowledge that these controls would further isolate the respective contributions of advantage proportionality and behavioral localization, and leave them for future investigation.

W2.1 & Q3 — Position C³ against VETTA, FACTOR, CrEST, and a plain min(Â, 0) clamp. Which already provide local credit correction, and what does confidence weighting add?

A: We thank the reviewer for pointing out these related works. We agree that reinforcing undesirable intermediate behaviors is not a newly identified phenomenon; our contribution is to characterize this issue in multi-turn agent RL and propose a targeted correction mechanism. VETTA can change token-level credit signs through value residuals, and CrEST explicitly separates credit direction from magnitude. FACTOR uses nonnegative token weights to allocate action credit while preserving its sign. C³ differs by using detector-identified behavioral events to selectively reverse positive advantages after estimation, without modifying rewards, returns, or critic targets.

Unlike a simple min⁡(A^i,0)\min(\hat A_i,0) clamp, C³ reverses positive credit proportionally to the original advantage and policy confidence, while preserving non-positive advantages. Our ablation shows that C³ and constant κ=1\kappa=1 achieve comparable task accuracy (50.20 vs. 50.16), but C³ yields fewer query loops (69 vs. 147) and behavior-union violations (90 vs. 218). This supports the benefit of confidence-guided correction beyond constant-strength reversal.

AuthorsOpenReview ↗

Response to Reviewer QeQG (2)

W2.2 — How were the qualitative case studies selected, and what can they establish about local corrections?

A: We thank the reviewer for pointing out the need to clarify both case selection and interpretation. The Search QA and WebShop examples are illustrative cases selected to demonstrate specific behavior patterns, including query formulation, entity attribution, and purchase recovery. They are not intended to be representative samples or to establish statistical performance, which is evaluated on the full benchmarks.

As clarified in Appendix D.1, the examples compare trajectories independently generated by terminal-PPO and PPO+C³ on the same tasks, rather than matched trajectories or controlled interventions. We therefore agree that differences in subsequent actions and observations cannot be attributed solely to individual local corrections. We have revised the presentation accordingly, labeling the WebShop examples by policy rather than as before/after correction. These cases illustrate differences between learned policies, not trajectory-level causal effects.

W2.3 — Does C³ generalize beyond filtered SFT initializations and existing agent-RL recipes?

A: We thank the reviewer for raising this concern. To examine C³'s compatibility with different agent-RL recipes and environments, we expanded the T²PO evaluation and added AppWorld experiments. The results are summarized below.

SettingTraining recipeInitializationEvaluation metricBaseline+ C³
Search QAT²PO (GiGPO-style)Existing SFT initializationMacro strict EM51.0551.49
WebShopT²PO (GiGPO-style)Existing SFT initializationTask score86.5289.09
AppWorldGDPOOriginal Qwen3-8B, no task-specific SFTTest-N TGC Avg@438.84 ± 3.71%41.52 ± 2.97%
AppWorldGDPOOriginal Qwen3-8B, no task-specific SFTTest-C TGC Avg@418.82 ± 1.50%19.84 ± 1.01%

For AppWorld, both GDPO and GDPO+C³ use the same 90 training tasks, 32 sampled trajectories per task, and 90 RL updates. Evaluation uses 168 held-out Test-N tasks and 417 held-out Test-C tasks, with four sampled trajectories per task under the same ReAct protocol. C³ improves TGC by 2.68 and 1.02 percentage points, respectively; ± denotes the sample standard deviation across the four rounds. Before RL, Qwen3-8B reaches 22.92% on Test-N and 10.37% on Test-C. These results extend the evidence beyond the filtered-SFT setting in Appendix A.3 and support C³'s compatibility with different agent-RL recipes and training initializations.

Q2 — Please report the full checkpoint-selection protocol. Is selection disjoint from reporting, and how do the results compare with final or last-N checkpoints?

A: We thank the reviewer for highlighting the ambiguity in our checkpoint reporting. The original Table 6 reported the maximum validation value of each metric within the displayed training window. Consequently, the success rate and task score of T²PO+C³ came from different checkpoints (iterations 120 and 130, respectively), rather than being jointly evaluated at the same checkpoint. We have therefore removed the original Table 6 and replaced it with Avg@4 evaluations of T²PO and T²PO+C³ at their respective peak checkpoints, using the same fixed 500-task benchmark.

For the main results, Table 1 (Search QA) uses the final checkpoint after one training epoch, whereas Table 2 (WebShop PPO/GDPO/T²PO) reports peak-validation-checkpoint results. This selection is motivated by training collapse observed in some WebShop runs. We acknowledge that checkpoint selection and reporting use the same 500-task benchmark rather than disjoint task sets. Thus, the reported WebShop results should be interpreted as peak-checkpoint performance. We have not completed a uniform final-checkpoint and last-N comparison for all WebShop arms.

Q3 — How does C³ degrade with noisy detectors or learned judges?

A: We thank the reviewer for raising this important question. Our existing experiments already use an imperfect detector rather than assuming noise-free behavioral labels. In an audit of 427 query-level items, the detector achieves 95% precision for identifying repeated information needs and 90% precision for unnecessary repeated searches, providing initial evidence that C³ can work despite detector errors.

False positives may incorrectly suppress desirable behaviors, whereas false negatives leave undesirable behaviors uncorrected. The AppWorld training logs also confirm that C³ performs actual advantage reversal on 116,144 of 15,846,833 generated tokens (0.733%), across 55 of 90 update batches. C³ can accommodate learned judges that provide localized spans and severity scores through the same interface. However, we have not systematically evaluated controlled detector-noise levels or LLM-based judges, and therefore leave their robustness evaluation for future work.

AuthorsOpenReview ↗

Gentle Reminder Regarding the Rebuttal Deadline

Dear Reviewer QeQG,

As the rebuttal period is approaching its deadline, we would like to kindly follow up on our responses and share one additional experiment addressing your question about sign reversal versus positive-credit removal.

Specifically, we added a positive-only advantage clamping baseline, min⁡(A^i,0)\min(\hat A_i,0), which removes positive credit on flagged spans while preserving negative credit. In contrast, C³ reverses positive advantages into negative ones, with the correction magnitude further modulated by the behavioral confidence. The results across the seven Search QA benchmarks are summarized below:

Search QA benchmarkPPO+C³PPO+CLAMP
NQ39.5 ± 0.340.04 ± 0.17
TriviaQA63.5 ± 0.162.11 ± 0.09
PopQA45.0 ± 0.344.35 ± 0.16
HotpotQA55.6 ± 0.155.49 ± 0.29
2Wiki67.9 ± 0.364.20 ± 0.19
MuSiQue29.7 ± 0.128.69 ± 0.39
Bamboogle50.4 ± 0.047.60 ± 2.15
Macro strict EM (%)50.20 ± 0.1048.93 ± 0.24

C³ achieves a 1.27 percentage-point improvement over positive-only clamping, outperforming it on six of the seven benchmarks. We hope this additional comparison helps clarify the benefit of sign reversal beyond simply removing positive credit.

We would greatly appreciate it if you could take another look at our updated responses when time permits. Thank you again for your time and valuable feedback!

Reviewer_xF2AOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper proposes C³, a confidence-guided credit correction method for multi-turn LLM reinforcement learning. C³ identifies undesirable behavior spans and selectively reverses their positive token-level advantages, with correction strengths determined by policy confidence. Experiments on Search QA and WebShop demonstrate improvements under critic-based and critic-free RL methods.

Critical strengths
  1. Practical approach to an established challenge. Fine-grained credit assignment for intermediate behaviors is a well-recognized problem in multi-turn RL. C³ offers a simple, plug-and-play correction mechanism that can be integrated into existing RL pipelines without modifying the underlying advantage estimator.
  2. Useful behavioral and credit analyses. The paper examines positive advantages assigned to undesirable behaviors and tracks their occurrence during training. These analyses provide useful empirical observations about how local credit correction affects agent behavior.
Critical weaknesses
  1. Limited novelty relative to existing fine-grained supervision methods. Prior work, particularly TEXT2GRAD [1] and GEAR [2], has explored using localized feedback to adjust token- or span-level policy optimization. Although C³ differs in its supervision source and post-estimation correction mechanism, its distinct methodological contribution remains insufficiently established.
  2. Insufficient evidence for the effectiveness of confidence guidance. While confidence-guided correction is the central component of C³, Table 3 only compares different confidence aggregation strategies. Without simpler controls such as constant-strength advantage reversal or masking positive advantages, it is unclear whether confidence guidance provides meaningful benefits beyond basic local credit correction.
  3. Limited experimental coverage and generalization evidence. The experiments are restricted to Search QA and WebShop, each evaluated with a single model backbone, and comparisons with recent fine-grained credit assignment methods are limited. This narrow evaluation does not sufficiently establish generalization to more diverse and challenging interactive agent environments, such as AppWorld [3], WebArena [4], or AgentSense [5].
  4. Potential confounding factors in PPO baseline comparisons. Appendix B.2 indicates that terminal PPO incorporates process penalties into the terminal reward, whereas PPO+C³ uses outcome-based advantages followed by actor-side correction. These differences in reward construction complicate the attribution of performance gains specifically to C³.
  5. Limited justification of credit misalignment. Figure 3(c) shows that 29.07% of tokens within detected undesirable-behavior spans receive positive advantages. However, positive sampled advantages do not necessarily indicate incorrect causal credit assignment, and the paper provides limited direct evidence that C³ produces more accurate local credit.

References

[1] TEXT2GRAD: Reinforcement Learning from Natural Language Feedback. ICLR 2026.

[2] GEAR: Granularity-Adaptive Advantage Reweighting for LLM Agents via Self-Distillation. arXiv:2605.11853, 2026.

[3] AppWorld: A Controllable World of Apps and People for Benchmarking Interactive Coding Agents. ACL 2024.

[4] WebArena: A Realistic Web Environment for Building Autonomous Agents. ICLR 2024.

[5] AgentSense: Benchmarking Social Intelligence of Language Agents through Interactive Scenarios. NAACL 2025.

Questions for authors

See Weakness.

3 comments
AuthorsOpenReview ↗

Response to Reviewer xF2A (1)

We thank the reviewer for recognizing the practical simplicity of C³ and for highlighting the need to better establish its methodological contribution. In response, we have clarified its distinction from existing local credit-assignment methods and added controlled ablations to examine the contribution of confidence-guided correction.

W1 — Limited novelty relative to existing fine-grained supervision methods.

A: We thank the reviewer for pointing out these related approaches. Our core contribution is identifying and addressing a fundamental mismatch between estimated advantages and actual behavioral quality, rather than simply providing finer-grained supervision.

TEXT2GRAD learns token-level rewards and feeds them into return and advantage estimation. GEAR uses a ground-truth-conditioned teacher to identify regions and reweight their advantages. C³ instead takes the base optimizer's advantages as input and replaces a flagged positive coefficient with −κqÂ. The correction requires neither a learned process-reward model nor a teacher forward pass. It leaves the base reward and credit estimator intact while changing the actor update on the selected spans. In addition, experiments further demonstrate improved task accuracy and substantially reduced undesirable behaviors across different RL optimizers. We will incorporate this discussion and clarify the distinction from prior work in the revised version.

W2 — Insufficient evidence for the effectiveness of confidence guidance.

A: We thank the reviewer for suggesting more direct controls for confidence guidance. The added controls show that confidence guidance suppresses more detected undesirable behavior while maintaining task accuracy comparable to constant-strength reversal. The revised Section 6.2 and Figure 7 compare confidence, constant strength, and whole-bad-turn masking:

Training ruleMacro strict EM (%)Detected query loopsDetected behavior union
C³50.20 ± 0.1069/206,852 = 0.0334%90/206,852 = 0.0435%
Constant κ=150.16 ± 0.25147/206,852 = 0.0711%218/206,852 = 0.1054%
Whole-bad-turn masking48.74 ± 0.25466/206,852 = 0.2253%553/206,852 = 0.2673%

C³ and constant κ=1 reach comparable strict EM (50.20% and 50.16%), while C³ produces fewer detected query loops and less than half the overall violation rate. Accuracy follows the endpoints in Figure 7 (left); the behavior comparison uses 51,713 questions × four generations per policy. Figure 7 (right) shows the C³–constant comparison, while the table also includes masking. Appendix B.3 gives the error-bar definitions.

Confidence measures how strongly the policy favors its sampled action, rather than whether that action is correct. Once a behavior is identified as undesirable, stronger policy preference motivates stronger correction. Span-level aggregation assigns a consistent strength to the tokens in the same behavioral event. The masking control, by contrast, removes both positive and negative advantages on the marked turn; a positive-only clamp remains a distinct control.

W4 — Potential confounding factors in PPO baseline comparisons.

A: We thank the reviewer for highlighting this potential confound. We added a Search QA experiment combining terminal behavioral penalties with C³. In this recipe, detector-based penalties enter the terminal reward before GAE, and C³ then corrects the resulting token-level advantages before the actor update. Section 5.1 describes this combination, and Table 1 reports:

Search QA recipeMacro strict EM (%)
PPO + terminal47.79 ± 0.50
PPO + C³50.20 ± 0.10
PPO + terminal + C³50.41 ± 0.35

The added terminal+C³ recipe is 2.62 points above PPO + terminal, with higher scores on all seven benchmarks. This expands the evaluation to C³ applied on top of terminal behavioral penalties. The reward-side penalties and actor-side correction are distinct operations: the former modify returns before GAE, while C³ operates on the estimated advantages without further changing the rewards or returns.

AuthorsOpenReview ↗

Response to Reviewer xF2A (2)

W3 — Limited experimental coverage and generalization evidence.

A: We thank the reviewer for recommending evaluation in additional interactive environments. Given the limited time and computational resources during the rebuttal period, we extended our evaluation to two additional benchmarks, AppWorld and AgentSense, covering application-API interaction and social interaction, respectively.

AppWorld. To examine whether C³ can work without task-specific SFT, we additionally trained GDPO and GDPO+C³ directly from the original Qwen3-8B model. Given the limited time and GPU resources available during the rebuttal period, we adopted a controlled training setup with 90 training tasks, 32 sampled trajectories per task, and 90 RL updates. Both arms use identical training and evaluation protocols.

AppWorld policyTest-N TGC (%)Test-N SGC (%)Test-C TGC (%)Test-C SGC (%)
Qwen3-8B before RL22.92 ± 0.777.14 ± 3.5710.37 ± 0.772.34 ± 0.69
+ GDPO38.84 ± 3.7119.64 ± 4.8418.82 ± 1.506.83 ± 0.93
+ GDPO + C³41.52 ± 2.9722.77 ± 3.0519.84 ± 1.017.19 ± 1.02

Evaluation covers 168 held-out Test-N tasks and 417 held-out Test-C tasks, with four trajectories per task. TGC measures task goal completion, while SGC measures completion of all three tasks in a scenario. C³ improves TGC by 2.68 and 1.02 percentage points on Test-N and Test-C, respectively, with higher mean SGC on both splits. These results extend our evaluation beyond filtered-SFT initialization to direct RL from a general-purpose base model.

AgentSense. We further evaluate the final Search QA checkpoints on 1,225 social interaction scenarios, without additional training. All policies use the same DeepSeek-v4.1-flash partner and single-judge evaluation protocol.

PolicyGoal attainment (%)All goals completed
Search SFT76.33755/1,225 (61.63%)
PPO + terminal77.70772/1,225 (63.02%)
PPO + process76.73751/1,225 (61.31%)
PPO + C³78.46790/1,225 (64.49%)
PPO + terminal + C³78.79787/1,225 (64.24%)
GDPO77.65779/1,225 (63.59%)
GDPO + C³77.49779/1,225 (63.59%)
T²PO76.81763/1,225 (62.29%)
T²PO + C³77.47774/1,225 (63.18%)

C³ improves goal attainment by 0.76 percentage points with PPO and 0.66 points with T²PO, while GDPO remains comparable. The 95% template-bootstrap intervals include zero, so we interpret these as encouraging point-estimate trends rather than statistically established improvements. Overall, AppWorld and AgentSense extend the evaluation to application-API and social interaction settings, respectively.

W5 — Limited justification of credit misalignment.

A: We thank the reviewer for asking us to clarify what the credit audit establishes. The audit measures a conflict between the specified behavioral constraint and the local training coefficient; it does not estimate an action's ground-truth causal contribution. A token is counted when it belongs to a detector-flagged span and still receives positive base advantage. Over the common training window of rollouts 50–832, this occurs for 18,460/63,511 = 29.07% of marked valid tokens in PPO and 7,468/21,535 = 34.68% in GDPO.

A successful trajectory can contain a redundant query or an invalid action that the agent later recovers from. Outcome-based credit can still assign a positive coefficient to that local behavior. C³ expresses the additional preference that a detected violation should not receive positive local reinforcement. Its purpose is to enforce that preference in the actor update, rather than recover a counterfactual value from the detector.

We therefore use the token audit to motivate the correction, and the task and behavior evaluations to assess its effects.

AuthorsOpenReview ↗

Gentle Reminder Regarding the Rebuttal Deadline

Dear Reviewer xF2A,

As the rebuttal period is approaching its deadline, we would like to kindly send a gentle reminder regarding our responses. We have further updated the rebuttal with an additional experiment directly comparing C³ against positive-only advantage clamping.

The detailed results across seven Search QA benchmarks are provided below:

Search QA benchmarkPPO+C³PPO+CLAMP
NQ39.5 ± 0.340.04 ± 0.17
TriviaQA63.5 ± 0.162.11 ± 0.09
PopQA45.0 ± 0.344.35 ± 0.16
HotpotQA55.6 ± 0.155.49 ± 0.29
2Wiki67.9 ± 0.364.20 ± 0.19
MuSiQue29.7 ± 0.128.69 ± 0.39
Bamboogle50.4 ± 0.047.60 ± 2.15
Macro strict EM (%)50.20 ± 0.1048.93 ± 0.24

C³ improves the average macro strict EM by 1.27 percentage points over positive-only clamping, outperforming it on six of the seven benchmarks. We hope this additional experiment helps clarify the benefit of sign reversal over simply removing positive credit.

We would greatly appreciate it if you could review our updated responses when time permits. Thank you again for your time and consideration!

Comments on the paper

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AuthorsOpenReview ↗

Summary of Additional Experiments and Rebuttal Updates

Dear Reviewers and Area Chairs,

We sincerely thank all reviewers for their thoughtful and constructive feedback. Below, we summarize the main additions and findings.


1. Expanded Evaluation Across Agent-RL Recipes and Interactive Environments

Concern: The original evaluation provides limited coverage of existing agent-RL methods and interactive environments, and the generality of C³ beyond filtered SFT initializations remains unclear.

New Experiments: We extended the evaluation with T²PO, AppWorld, and AgentSense. In particular, AppWorld experiments start directly from Qwen3-8B without task-specific SFT, while AgentSense evaluates the transfer of existing Search QA checkpoints to social interaction scenarios.

Main Findings:

(a) Compatibility with different agent-RL recipes

EvaluationT²POT²PO+C³Improvement
Search QA macro strict EM51.0551.49+0.44
WebShop task score86.5289.09+2.57
WebShop success (%)76.5076.70+0.20

(b) AppWorld: RL without task-specific SFT

MetricTest-N GDPOTest-N GDPO+C³Test-C GDPOTest-C GDPO+C³
TGC (%)38.84 ± 3.7141.52 ± 2.9718.82 ± 1.5019.84 ± 1.01
SGC (%)19.64 ± 4.8422.77 ± 3.056.83 ± 0.937.19 ± 1.02

C³ improves TGC by 2.68 percentage points on Test-N and 1.02 points on Test-C, extending the evaluation beyond the filtered-SFT setting.

(c) AgentSense: Transfer to social interaction

PolicyGoal attainment (%)All goals completed
PPO + terminal77.70755/1,225
PPO + C³78.46790/1,225
PPO + terminal + C³78.79787/1,225
GDPO77.65779/1,225
GDPO + C³77.49779/1,225
T²PO76.81763/1,225
T²PO + C³77.47774/1,225

These results extend the evaluation to social interaction. The observed differences are modest, and the 95% template-bootstrap intervals include zero.


2. Additional Controls for Confidence-Guided Correction and Sign Reversal

Concern: It remains unclear whether confidence weighting and sign reversal provide benefits beyond constant-strength correction or simply removing positive credit.

New Experiments: We added constant-strength correction, whole-bad-turn masking, and a positive-only advantage clamping baseline.

Main Findings:

Correction ruleMacro strict EM (%)
Token probability44.73 ± 0.18
Geometric span mean49.06 ± 0.22
Constant κ = 0.546.56 ± 0.44
Constant κ = 1.050.16 ± 0.25
Whole-bad-turn masking48.74 ± 0.25
Positive-only CLAMP48.93 ± 0.24
C³50.20 ± 0.10

The positive-only CLAMP sets positive advantages on flagged spans to zero while preserving negative advantages. C³ instead reverses positive advantages into negative ones. C³ outperforms positive-only CLAMP by 1.27 percentage points, with higher EM on six of seven Search QA benchmarks.

At comparable task accuracy, C³ also produces fewer detected query loops (69 vs. 147) and behavior-union violations (90 vs. 218) than constant κ = 1.0 in the separate four-generation evaluation.

These controls provide additional evidence for the benefits of confidence-guided sign reversal over constant-strength correction and simple positive-credit removal.


3. Additional Analyses and Methodological Clarifications

Beyond the new experiments above, we conducted further analyses and clarified several aspects of the methodology and evaluation:

  • Training-time correction coverage: Recovered complete actor-training statistics, showing that corrections affect 18,460 PPO tokens and 10,465 GDPO tokens, distributed across 43.17% and 16.21% of training update batches, respectively.
  • 2Wiki performance reversal: Conducted a fine-grained question-type and answer-type analysis, identifying yes/no answer selection as a major source of the opposite PPO and GDPO trends.
  • Detector reliability: Audited 427 query-level items, obtaining 95% precision for repeated information needs and 90% precision for unnecessary repeated searches, and evaluated sensitivity to four similarity thresholds.
  • Checkpoint selection: Clarified final- and peak-checkpoint protocols, including the use of the same 500-task benchmark for WebShop selection and reporting.
  • Qualitative examples: Clarified case selection and distinguished comparisons between independently generated policy trajectories from causal attribution to individual local corrections.
  • Statistical limitations: Explicitly distinguished evaluation-sampling variance from independent training-seed variance and clarified the scope of our robustness claims.

We sincerely appreciate the reviewers' time and valuable feedback. Their comments have substantially improved both the rigor and clarity of our work.

Best regards,

The Authors

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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